An OXICM group interested in Critical Care journals

Hi all, and welcome. This site is designed to co-ordinate the activities of the Critical Care Journal Clubs within the Oxford region. There will be ~ weekly “scoops” from the Oxford JC (Friday mornings at the John Radcliffe) with more content and links currently in the planning stages.

Percutaneous tracheostomy (PT) and surgical tracheostomy (ST) are performed in critical care for a variety of indications. Three previous meta-analyses had demonstrated mixed results with limited data on survival and long term complications. With the introduction of newer PT techniques, the authors felt further analysis was warranted.

Warning! This study uses multiple abbreviations which I have listed at the end of this review.

Aim

The aim of this study was to conduct a meta-analysis to determine whether percutaneous tracheostomy techniques are advantageous over surgical tracheostomy and if one percutaneous technique is superior to the others.

Methods

The authors searched CENTRAL, MEDLINE and EMBASE databases for RCTs and also society meetings for unpublished data between 1966 – 2013. Their search had no language restrictions and included adult, mechanically ventilated patients. They excluded non RCTs, cross over studies, emergency airways, paediatrics and non-critically ill/home ventilated patients. Primary outcomes during the procedure included major and minor bleeding, technical difficulties, false route, subcutaneous emphysema, pneumothorax and oxygen desaturation, and post procedure included major and minor bleeding, stoma inflammation or infection, tracheomalacia and tracheal stenosis. Secondary outcomes included length of procedure and hospital survival.

Results

11625 citations were screened, 108 were retrieved for more detailed evaluation. Of these, 22 citations were included in the meta-analysis. 16 of these were a mixed patient population with one trauma, one surgical and four not described. Most ST were performed by surgical specialties (surgeons (10) and ENT (3)) and PT by intensivists (12), surgeons (4) and ENT (3). All PT occurred in ICU. Bronchoscopy was used regularly in 9 studies.

This meta-analysis is relevant to our current practice. This study has clearly defined objectives and conducted a comprehensive literature search seeking out non published RCTs with no language restrictions. Inclusion and exclusion criteria are defined and appropriate. Data extraction is detailed along with how disagreements were resolved and evaluation of publication bias. Multiple PT techniques are explored which may be of particular interest in institutions that use certain techniques exclusively.

Weaknesses

Other outcomes that may have been of interest include tracheostomy blockage, accidental decannulation and re-intubation rates. There is no information on the length of stay of patients and the duration of mechanical ventilation (pre procedure and total). The authors stated that this meta-analysis would be useful given the introduction of newer PT techniques, yet ultrasound is not commented on.

One study accounted for 39% of the weight in the pooled effects of Pt Vs ST. This study used a TLT technique but we had not heard of, seen, or used this technique.

The majority of I2 values for pooled PT Vs ST outcomes are 0%. This raised some discussion amongst our audience given the apparent heterogeneity of the RCTs in the brief descriptions provided in the appendices. Most studies excluded patients in whom a surgical tracheostomy would have probably been first choice, due to the presence of contraindications to the PT technique, and it is difficult to know how this affected the results.

Will this change my practice?

This meta-analysis does not provide a clear benefit of PT over ST to alter current practice locally. The RCTs included are not wholly representative of current practice and therefore I would have concerns about the external validity of this paper. However, this meta-analysis raised important questions about the role of PT and ST, including patient selection, technique, and more broadly, training opportunities.

The Surviving Sepsis Campaign recommends red blood cell (RBC) transfusion should occur if the haemoglobin (Hb) concentration decreases to <7 g.dL-1 and to target an Hb of 7-9 g.dL-1once tissue hypoperfusion has resolved. During this period of hypoperfusion, practice has been guided by the results of the trial by Rivers et al where the transfusion threshold was a haematocrit of 30% (which approximately equates to an Hb of 9-10 g.dL-1. The landmark TRICC trial concluded that a restrictive transfusion strategy was at least as effective as and possible superior to a liberal transfusion strategy expecting in patients with unstable angina and acute myocardial infarction – two areas in which the evidence base is still unclear to this day. Since then, studies in different settings (cardiac surgery, orthopaedic surgery, acute GI haemorrhage) and a Cochrane systematic review in 2012 consisting of 6294 patients have all shown that a restrictive transfusion strategy is associated with less RBC transfusions without any apparent harm.

These investigators set out to investigate the effects of a lower versus higher transfusion threshold on mortality in patients with septic shock in critical care. They conducted a multi-center randomized, stratified, parallel controlled trial involving 32 Scandinavian general ICUs over a two-year period. Randomization was performed using a centralized computer-generated assignment sequence in a 1:1 ratio with permuted blocks of varying sizes. The investigators assessing mortality, data and safety monitoring committee and trial statistician were all blinded. Due to the nature of the intervention, it was not possible to ‘blind’ the patient or attending clinician. They performed an intention-to-treat analysis. Their power calculation was based on the ‘severe infection’ subgroup of the TRICC trial (relative risk reduction of 20% in restrictive group) and they calculated that 1000 patients would be needed to show a 9% reduction in the absolute risk assuming a mortality of 45% in the liberal group (based on regional cohort data).

The PICO analysis is as follows:

Patients

Inclusion criteria were adult patients (>18 years old) with septic shock and Hb <9 g.dL-1. Exclusion criteria were reasonable and excluded patient groups in whom the transfusion evidence-base is not quite clear/limited – life threatening bleeding and acute coronary syndromes. A total of 1,224 patients were assessed for eligibility and eventually 503 patients were randomized to the ‘lower threshold’ group and 497 to the ‘higher threshold’ group. Baseline characteristics were similar in both groups. Subgroup analyses were carried out in the following groups – presence/absence of chronic cardiovascular disease, age less than/greater than 70, and a SAPS II score of above 53 versus below 53.

Primary outcome – 90-day mortality – data was available for 998/1005 patients and showed no significant difference between both groups (per-protocol populations). 216 patients (43%) in the lower threshold group and 223 patients (45%) in the higher threshold group had died (RR 0.94, 95% CI 0.78 – 1.09, p = 0.44). There was also no significant difference in secondary outcomes – use of life support (vasopressor or inotropic therapy, mechanical ventilation, or RRT) at days 5, 14 and 28 after randomization, incidence of adverse and ischaemic events, percentage of days alive without life support and percentage of days alive and out of the hospital. There was a significantly lower proportion of RBC transfusions in the restrictive group compared to the liberal group (1545 units vs. 3088 units, p<0.001). In addition, a total of 176 patients (36%) did not receive RBC transfusion at any point. There were no significant differences in the subgroup analyses either.

Strengths

There are many strengths of this trial. The randomization process appears robust. The blinding is acceptable given the nature of the intervention. There is a high recruitment rate – 1005 out of 1224-screened patients ended up being randomized. The statistics and power calculation are reasonable – using the data from the TRICC trial, albeit old, is probably justified given the lack of evidence in this area. Primary outcome data was available for 99.2% of patients and the investigators’ went to good lengths to try obtaining primary outcome data even when patients were discontinued from the study for whatever reason. Another potential strength is the short time between trial completion (December 2013) and publication (2014). The authors also comment that the trial was pragmatic as it did not affect any other aspects of care.

Weaknesses/Limitations

This trial does not specifically answer the question of what the transfusion threshold should be during the EGDT window i.e. during the first 6 hours whilst in A&E and little information is available about what happened during that time period. The ARISE and PROCESS trials hopefully shed some light on this. There was a significant delay from time of randomization to first day of treatment – median times were 15 and 14 hours in the lower threshold and higher threshold groups respectively. Protocol violations occurred in both groups – 10% of patients in the ‘lower threshold’ group received transfusion despite being above the transfusion threshold. However, there was still a significant difference in the daily Hbs in both groups and the authors carried out a per protocol analysis which showed no overall difference between both groups. It is worth questioning why their mortality rate of patients with septic shock is 40 – 45% – this is in contrast to mortality data from the ARISE and PROCESS trials which quote a mortality of approximately 20%.

Will this change my practice?

Probably not. A transfusion threshold of 7 g.dL-1 when compared with 9 g.dL-1 results in no difference in mortality and morbidity in critical care patients suffering from septic shock. These findings are in keeping with other trials in other medical/surgical settings. This work also supports the clinical practice of majority of the clinicians who attended the journal club meeting. The results of trials in high-risk groups e.g. ACS are awaited.

Candida is a mould that is not infrequently isolated from cultures of ICU patients, and in the appropriate clinical context, can be diagnostic of invasive candidal infection. Unfortunately, invasive candidiasis in ICU is associated with significant morbidity and mortality, and as such, strategies to prevent or treat this condition are needed. Many strains of candida including glabrata and krusei are resistant to the azole drugs such as fluconazole, therefore echinocandin drugs such as caspofungin, which inhibits fungal cell wall synthesis, are increasingly used. Delays is antifungal treatment have been found in retrospective studies to be associated with poor outcome. To date, only in specific patient subsets (eg transplant, pancreatitis, neonates) has antifungal prophylaxis been shown to improve outcome.

These investigators set out to test the hypothesis that fungal prophylaxis in general at-risk ICU patients could reduce the incidence of invasive candidiasis. They carried out a multicentre randomised double-blind placebo-controlled trial in ICU patients at high risk of invasive candidiasis. Included patients had to meet all of the following criteria: non-pregnant adult, mechanical ventilation, ICU stay > 48 hours, central venous catheter used, broad spectrum antibiotic given, plus one of TPN/pancreatitis/dialysis/major surgery/steroids/other immunosuppressants. Neutropenic patients were excluded.

A total of 219 patients were enrolled and randomised in 15 ICUs in the US. It is important to note that 33 of these patients were immediately excluded at enrolment as per the protocol because they were found to have invasive candidiasis at baseline, and began caspofungin treatment. The diagnosis of invasive candidiasis was made by either positive cultures (ie: proven), or a positive 1,3 beta D glucan serological test in the context of a sepsis syndrome (ie: probable). The remaining “modified intention to treat” patients amounted to 84 in the placebo group and 102 in the caspofungin group (it’s not entirely clear why there is such a discrepancy in numbers). The headline results are that there was no difference in the primary outcome, which was proven or probable invasive candidiasis (9.8% v 16.7%, p = 0.14). There was also no difference between the groups in terms any secondary outcomes including mortality and length of stay. Safety outcomes were not different between the groups.

Having stated the above results for the modified intention to treat group, the authors go on to repeat the analysis with the 33 initially candidiasis-positive patients re-included. This analysis shows a significantly lower rate of candidiasis in the caspofungin group: 18.8% versus 30.4%, p = 0.04. We should remember that this pre-emptive analysis is based on a serological test not a microbiological one, and that the 33 patients included in this analysis did not end up being randomised and their treatment was not blinded. So it’s probably not an internally valid finding and the specified outcomes and analyses are somewhat confusing. But the authors claim this is a useful pre-specified analysis because it serves as a proof of concept for initiating pre-emptive antifungal therapy using the 1,3 beta D glucan assay.

In terms of wider applicability, the glucan assay is not widely available in UK ICUs, and there are doubts about its usefulness as a diagnostic test. Furthermore the incidence of invasive candidiasis in the patients studied was much higher than in other ICU studies and higher than in UK general ICUs. It’s also a relatively small study number for a multicentre comparative effectiveness trial.

What we can probably take from this paper is that, although it may be an apparently safe antifungal drug in ICU, there is no benefit of caspofungin as a pre-emptive or prophylactic agent for invasive candidiasis in the at-risk general ICU patient. Echinocandins are expensive and, in view of emerging antifungal resistance, should be used only where there is a proven benefit.

What type of non-invasive respiratory support is best in acute pulmonary oedema? Broadly speaking, non-invasive respiratory support is divided into CPAP (a constant positive pressure is applied throughout respiration) and bilevel ventilation (the ventilator delivers a higher “inspiratory” pressure during inspiration and a lower “expiratory” pressure the rest of the time). Both modes have been used to treat respiratory failure due to pulmonary oedema, and these authors have set about comparing them in a meta-analysis.
The story stretches as far back as 1997 when Mehta et al published a small trial comparing bilevel NIV with CPAP for acute pulmonary oedema. 27 subjects were randomised; there was no difference in outcome, although a trend towards more myocardial infarction in the bilevel group was observed.
A handful of subsequent trials have since showed equivalence between the two modes for pulmonary oedema. In these, the concerns over excess cardiac events have not been consistently replicated. A major milestone was the UK-based 3CPO trial published in 2008 – this eclipsed all the other trials combined in terms of subject numbers. 1069 adults with cardiogenic pulmonary oedema and a pH < 7.35 were randomised 1:1:1 to oxygen therapy, bilevel NIV, or CPAP. There was no difference between the two latter groups (7 day mortality was 9.6% versus 9.4% (and 9.8% in the oxygen group)) and no difference in other outcomes.
This new meta-analysis attempts to combine the data of all randomised trials from 1966 to date comparing bilevel NIVand CPAP for acute cardiogenic pulmonary oedema. The four outcomes studied are mortality, intubation, MI and length of stay. 12 trials are included, amounting to 1433 patients, of which over half are from the 3CPO dataset. Inherent difficulties in this field of critical care research include: inconsistent terminology which affects search criteria, difficulties in defining cardiogenic as opposed to non-cardiogenic pulmonary oedema, and heterogeneity in ventilator pressures delivered in different study arms. The latter point is important because CPAP ranges from 5 to 15 cmH2O (mean approx 10 cmH2O) whereas the low pressure in bilevel modes is invariably 5 cmH2O and the high pressure varies from 8 to 20 cmH2O.
The meta-analysis finds no difference between bilevel NIV and CPAP with respect to any of the specified outcomes. The funnel plot shows an acceptably low level of publication bias and study heterogeneity was not found to be significant. Of course, most of the trials were small, weren’t powered for all the outcomes quoted here, and none achieved blinding between the two modes.
Whether this article adds anything to our understanding of NIV is questionable. The reassuring lack of difference in MI rates is perhaps the most helpful finding for our future practice. We already know from trials of oxygen therapy versus non invasive respiratory support (of any kind) that the latter accelerates recovery, oxygenation and normalisation of physiological parameters in patients with pulmonary oedema. On this basis we should continue to use non-invasive techniques in acute pulmonary oedema of suspected cardiac cause. But… the question of which mode to use remains unanswered. Since the positive intrathoracic pressure is thought to mediate the physiological advantages of non invasive respiratory support, future trials should ensure that mean ventilator pressures are comparable between groups.

The use of albumin in the resuscitation and treatment of patients with shock, burns, hypovolaemia and other critical illness was commonplace in the second half of the 20th century. This was largely based on the observed association between hypoalbuminaemia and organ dysfunction/death.
Following a Cochrane meta-analysis in 1998 which showed lack of benefit and possibly an increased risk of death from albumin, the use of albumin in the UK ICU community fell sharply. However the subsequent SAFE trial showed absence of harm from 4% albumin (except in head injured patients) and possibly a signal towards benefit in the septic cohort. Since then albumin has remained a therapeutic option in the treatment of severe sepsis, and features in the Surviving Sepsis Guidelines “when patients require substantial amounts of crystalloids” with a grade 2C recommendation.
The Italian investigators behind the ALBIOS trial set out to pragmatically test the efficacy of albumin as an adjunctive resuscitation fluid in severely septic patients within 24 hours of diagnosis. 1818 patients in 100 Italian ICUs were enrolled. The intervention group received 300 ml of 20% albumin in addition to crystalloids until ICU discharge. The target albumin level was 30 g/L. Crystalloids were administered in both groups according to goal directed therapy for sepsis initially, and then at the discretion of the clinician. The trial ran from 2008 to 2013. Importantly, the administration of albumin was an unblinded intervention.
The primary outcome, 28d mortality, was unchanged: 31.8% in the albumin group and 32% in the crystalloid only group. There were no significant differences in the secondary outcomes either. In terms of clinical measures there was a negligible difference in MAP (77 v 79 mmHg), a very slightly lower heart rate (94 v 99 bpm), a very slightly higher CVP (11 v 10 mmHg), a slightly more negative fluid balance in the first seven days, and a higher serum albumin (30 g/L versus 23 g/L) in the albumin group. The daily total fluid administered to the two groups did not differ.
It is worth noting that the authors did a retrospective subgroup analysis of the 1121 patients who had septic shock, showing survival benefit from albumin (43.6% versus 49.9%), and correspondingly, a trend towards increased mortality with albumin in the patients without septic shock.
What can we make from these results? Most importantly, although there may be a physiological advantage of giving albumin in severe sepsis, and that 20% albumin may be safe, there isn’t any overall impact on patient outcome. The retrospective subgroup analyses probably aren’t interpretable due to bias.
This was a rigorously conducted single-country multicentre trial with clear objectives and a practical real-world approach. The patients probably reflect our UK practice, with a mortality from severe sepsis of 30%, age about 70 years, 60% medical and 35% emergency surgical, 80% mechanically ventilated and with a moderate severity of illness. However there are problems with the design. Firstly, the use of albumin was unblinded which makes it hard to assume that the patients were treated similarly in all other ways by the clinicians. Secondly, the design was based on a projected mortality rate was 45% whereas the actual mortality was just over 30%. Thirdly, the paper states that “synthetic colloids were not allowed” whereas the supplementary appendix details the protocol violations which include 23% of patients in each group receiving synthetic colloids at least once. Moreover, 37% patients in the crystalloid only group received albumin at least once, and the rules for albumin administration were violated at least once in 42% of patients in the intervention group. So perhaps the conduct was less rigorous than implied in the paper. Finally, the investigators used 20% albumin which differs from the 4% albumin used in the SAFE trial.
The other useful data from the supplementary appendix is the microbiological analysis, which shows: primary site of infection to be lung 40%, abdomen 40%, urinary tract 15%; rate of positive site culture 63%; rate of positive blood culture 33%; organism type to be Gram positive 14%, Gram positive 20%, mixed bacteria 6%, virus 1%, fungus 3%; antibiotics given at randomisation to 93%. These data are always of interest when comparing the study population to one’s day to day practice.
The message seems to be that albumin is relatively safe in severe sepsis but without appreciable benefit. There’s no benefit from targeting a higher serum albumin of > 30g/L per se. We await a response from the Surviving Sepsis Campaign, but given the expense of albumin, it is unlikely to be recommended for routine practice.

On the basis that statins have been shown to have cholesterol-independent immunomodulatory effects, and that the aetiology of sepsis-associated ARDS is almost certainly immunopathological, could statins improve outcome in patients with sepsis-associated ARDS?
Herein lies the rationale for the US NIH supported ARDSnet trial known as SAILS. Investigators enrolled statin-naive adult patients with a PF ratio of 300 or less within 48 hours of onset of sepsis-associated ARDS in 44 US centres starting in 2010. Patients in the intervention group received enteral rosuvastatin as a 40mg loading dose followed by 20mg daily until 3 days post ICU discharge. Patients in the control group received a placebo. The primary outcome was hospital mortality.

The projected enrolment was 1000 patients, however the trial was stopped by the DSMB because of futility after 745 patients had been enrolled. There was no difference in mortality between the two groups. Ventilator free days and other secondary outcomes did not differ either. Hepatic and renal failure were slightly more prevalent in the rosuvastatin group and derangements of liver biochemistry were also more common.
Therefore, on the face of it, rosuvastatin didn’t improve outcomes in ARDS from sepsis and may have had an adverse impact. However a few issues in trial methodology make this conclusion less robust. Firstly, the plasma levels of rosuvastatin achieved were lower than the target range, suggesting that the dose used may have been inadequate to detect any beneficial (or harmful) effect. Secondly, the decision to use rosuvastatin is brought into question. Other statins such as atorvastatin and simvastatin are more commonly used in medical practice (and would have accounted for the trends towards benefit observed in retrospective studies to date). These drugs are more lipophilic and have different tissue penetration than rosuvastatin, so can we really view all statins equally with respect to ARDS? Thirdly, the screening exclusion rate in the trial was high so the findings may not be applicable to our real-world patient cohort.
Whether or not this trial was a robust test of statin class-effects in sepsis-associated ARDS is questionable. However, the absence of any signal towards benefit probably supercedes the signals from prior observational data and consequently the evidence does not support the use of statins in our standard care of patients with sepsis-associated ARDS.

If the ICU nurse asks you to specify a target blood pressure, what do you say? Maybe a mean arterial pressure of 60 or 65… (and perhaps a bit higher in a head-injured patient).

It’s a fundamental question, with no clear answer, so where does this 65 mmHg come from?

Perhaps you could quote the surviving sepsis guidelines, which makes a strong (grade 1) recommendation for such a MAP target in septic patients. But, the guideline experts acknowledge that this ‘strong’ recommendation is based on low quality evidence (grade C), namely:

(i) it’s the target that was used in the often cited early goal directed therapy trial (in which it’s worth noting that the actual median MAPs achieved were higher: 81 +- 18 in the standard therapy and 95 +- 19 in the EGDT group).

(ii) experimentally, there is a threshold MAP for each organ below which auto-regulation fails, in other words perfusion (i.e. flow) becomes pressure dependent (perhaps 50 mmHg for the brain, 60 mmHg for the kidney… but… this is based on animal and healthy volunteer experiments and we don’t know what’s “normal” in acute illness).

Bearing in mind the shaky foundations for this often quoted and widely practised 65 mmHg target, Asfar et al investigated whether a MAP target higher than 65 mmHg might be beneficial in sepsis. In their paper they set out to compare a target of 80 to 85 mmHg against a target of 65 to 70 mmHg for a duration of 5 days in 776 septic shock patients enrolled within 6 hours in 29 centres in France. This was achieved using standard fluid and vasopressor protocols. They also postulated that a higher MAP target might have a more pronounced benefit in patients with chronic hypertension.

There was good separation between the two groups in terms of achieved MAPs, and this difference does appear from the data to be attributable to the significantly different doses of noradrenaline infused (rather than differences in fluid volumes or other catecholamines). The main finding is that there was no difference in the primary outcome, death at 28 days. This was 34% in the standard group and 36% in the high group and the two Kaplan Meier curves were identical. However in the prespecified chronic hypertension subgroup (which actually accounted for 40% of enrolled patients), there was an apparent benefit from a higher MAP target (52% versus 39% mortality). The hypertensive patients subject to the lower MAP target were also significantly more likely to require renal replacement therapy, which the higher MAP target seemed to abolish. There was a higher rate of AF in the high MAP group (26 v 11%) and a trend towards an excess of other cardiovascular adverse events.

Was it a rigorous trial? It’s strengths are that it was large, randomised, multi-centre, and real-world. The obvious limitation is the lack of blinding and placebo control, which is probably unavoidable in a pragmatic trial of physiological target ranges. The second problem is that it didn’t turn out to be trial of 65 to 70 versus 80 to 85; it was more like a trial of 72 to 77 versus 82 to 87. So it didn’t quite test the intended hypothesis (though there was a consistent 10 mmHg difference between the groups). Thirdly, the number of patients screened (4098) far exceeded the number eventually enrolled.

What can we conclude? Well, there’s no indication for a higher than ‘normal’ MAP target in sepsis. In people with chronic hypertension, perhaps a somewhat higher MAP target than ‘normal’ would be needed if renal injury is an endpoint worthy of avoiding (but this is not what the trial set out to demonstrate). The generalisability of the trial to UK sepsis practice is limited, partly because all the participating centres were in France but also because a large proportion of screened patients were excluded. Perhaps the most practically relevant finding is the consistent disparity between target and actual blood pressure achieved in critically ill patients on noradrenaline. So next time you prescribe a target MAP of 65 mmHg, it’s worth remembering that your patient might spend most of their time over 70 mmHg. And whether this is the most appropriate MAP to prescribe for your particular patient, who may or not have hypertension, remains to be discovered.